Your paper has been seen by two expert reviewers, who in principle think the paper is publishable but also raise some very important points, which are seconded from my side from an editor's point of view. Many of those you have already adressed in your reply. The most important points of criticism that I see reading the reviews and which you should alleviate in any revised version are:

1. Both reviewers conclude that the changes that you made to the model have not solved the problem. It added another fitting parameter/degree of freedom, which made the results better for some sites but worse for others. The explicit conclusion of your paper therefore should be that the inclusion of a temperature dependent activation energy is not the final answer to the problem. However, also negative results are worth publishing as they clear the field for work in other directions.

In that respect, I realized that you did not do an independent parameter optimization for activation energies in the case when the dust/Ca effect is included. I would urge you to do this, as otherwise a robust conclusion on the dust/Ca effect cannot be drawn.

2. As editor of climate of the past I am a little concerned that the paper is quite technical and intended for the specialists in firn modeling and thus thematically would be more in the scope of The Cryosphere or a similar journal. My hope was that you could elaborate more on the implications of your work on climate reconstructions. However, given the fundamental criticism of the reviewers on the possible improvement of our understanding in firnification modeling (see point 1) any paleoclimatic conclusions would hinge on the caveats of the model. In case you submit a revised version to CP, I would nevertheless urge you to add some more discussion on the paleoclimatic implications of your work and the limitations of these conclusions.

In summary, any revised version of ther paper should include all your point-to-point changes in response to the reviewer comments as well as to my points above. Due to the fundamental criticism by the reviewers a revised version would have to go through another round of reviews.

Breant et al. have been thorough in their revision, and address most of the comments. It is still a very long read, after which the reader is only a little bit wiser as to whether the glacial d15N problem is solved. This is not completely the fault of the authors of course; it seems that this long-standing problem is just very complicated to solve in a satisfactory manner. The new conclusion section has been much improved, because it is more honest about the shortcomings of the approach taken here (i.e. the approach of modifying the activation energy). From re-reading the paper, it seems to me that only the dust effect can explain the LGM d15N values at both EDC and EDML, whereas the modified activation energy only improves the d15N fit at EDC and not at EDML. This suggests that the activation energy may not be the solution after all. So perhaps a temperature-dependent dust effect is needed?

There are a few smaller issues from my previous review that were not completely satisfactorily addressed:

* Both reviewers argued that there is not really a good physical underpinning of the model. But Figure 2 still suggests a physical mechanism for each value of Q, even though Q3 is an order of magnitude too small to for any known process, and Q1 (suggested to be vapor diffusion) has a value that seems too high at Q1=110 kJ/mol. Vapor diffusion scales with the vapor pressure, and the enthalpy of sublimation in ice is only 51 kJ/mol.
Having an empirical model is fine of course, and it should be made more explicit that the final model Q factors do not correspond to known individual processes (unlike what is suggested by Fig. 2).

* In their preferred model (Table 1), process 1 (Q1 = 110 kJ/mol) doesn’t do much. At all relevant temperatures, process 2 is at least an order of magnitude larger.

* The authors did not do a clear significance test of the improvement of the model fit to present day observations (d15N, Delta-age). They do now state that the improvement is “insignificant”. This is not how it should be presented. Either the improvement is statistically significant (in which case you can call it an improvement), or the improved model fit is statistically not significant, in which case you must conclude that both models perform equally well. An insignificant improvement (L576) is not an improvement, and cannot be called such. The authors should instead state both models perform equally well.

* The authors include tests of Delta age, which is a big improvement. However, it is unclear where the delta-age “data” values (Table S2) come from. It is not easy to know Delta-age, unless one has a very accurate ice age scale (from layer counting or volcanic references), coupled with a very accurate gas age scale (e.g. from firn air sampling, or high-res CH4 data). Where do these numbers come from? In some cases they are different from published values.

A few other minor comments:

L 21: This is not exactly true. The modified activation energy did not work at EDML

L360: It still isn’t clear what is being optimized. Just the root mean square fit?

L595: again the authors argue for a “somewhat improved fit” at colder sites. Such statements can only be made if significant.

L627: An age distribution with a width of 20% of delta-age is much too wide. The Kohler et al.
2011 paper is very clearly flawed. It is very instructive to read the exchange between the author and reviewer for that paper (http://www.clim-past.net/7/473/2011/cp-7-473-2011-discussion.html) – where the reviewer is correct (in my view). The wide filter they use results in a large overshoot in CO2 of up to 35 ppm, which we now know is incorrect because of the high-res WAIS Divide record, which proves that the 35 ppm overshoot is only a fantasy and not real.

Figure 7: It seems that dust is much more efficient at solving the glacial d15N mismatch at EDML and EDC than the activation energy alone. This could be stressed more clearly.

L807-809: Again, only at EDC! At EDML it did not improve.

L926: Both reviewers agree that the physical basis for the new parameterization is unclear. Having a purely empirical model is fine with me, but it should be called empirical, rather than physically-based.

Thank you for carefully revising your manuscript on "Modelling firn thickness evolution..." The revised version has now been seen by one of the previous reviewers and myself and I am happy to say that the manuscript has improved significantly. It has met many of the reviewer comments, although the reviewer still assesses the paper not as a breakthrough in this long standing problem in understanding firnification. Nevertheless, I deem it important to provide this information to the wider scientific public as it may shape future research.

Accordingly, I support publicaton of the manuscript after some further minor revisions. These pertain the following points:

- to warn the reader, please make clear in the abstract and manuscript early on that the changes done in the model do not provide a solution to the firnifaction issue at all sites.
- explain more carefully how you quantified the model parameters in Table 1 and 3
- rephrase the discussion of the physical processes as outlined by the external reviewer.
- please include the corrections and clarify the points raised in my annotated pdf attached to my editor comment

After including these corrections please provide me with a short point-to-point list of the changes you carried out.

All firn densification models applied to deglaciations show a large disagreement with δ15N measurements at sites in East Antarctica, predicting larger firn thickness during the Last Glacial Maximum, whereas δ15N suggests a reduced firn thickness compared to the Holocene. Here we present modifications, which significantly reduce the model–data mismatch for the gas trapping depth evolution over the last deglaciation at the coldest sites in East Antarctica, to the LGGE firn densification model.

All firn densification models applied to deglaciations show a large disagreement with δ15N...